acceptodds
Under review as a conference paper at ICLR 2027

Scaling Temporal Causal Discovery to Millions of Variables

Abstract

Temporal causal discovery becomes prohibitively expensive as the number of variables grows: with N series and L lags, a method may need to consider N^2L candidate relationships. Yet many real temporal systems are sparse, with each variable depending directly on only a small fraction of the system. We exploit this structure with VL-PCMCI, a scalable causal discovery framework that separates cheap global screening from expensive causal reasoning. VL-PCMCI first screens all lagged pairs using GPU-accelerated matrix operations, performs causal discovery independently within sparse blocks, and then reconciles relationships across blocks. We characterize when this decomposition preserves causal decisions and identify three requirements: true causes must survive screening, tested non-edges must be given separating sets, and statistical testing must account for screening. Experiments show that VL-PCMCI maintains high accuracy while scaling substantially beyond existing temporal causal discovery methods, recovering nearly every true edge in planted systems with millions of variables. At this scale, computation is no longer the only bottleneck: false positives from data-dependent screening grow approximately quadratically unless the final tests account for selection. These results show that temporal causal discovery at millions of variables is computationally feasible while identifying the statistical conditions required for reliable discovery at this scale.

Primary area:
causal reasoning
Keywords:
causal discovery, temporal causal discovery, time series, PCMCI, conditional independence testing, scalability, screening, divide and conquer, selective inference, GPU

Reviews

Among:
Shape:
1234this paper, Top 30%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_6qamOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper aims to make temporal causal discovery feasible for very large systems. It proposes VL-PCMCI, which combines tiled correlation screening, sparse storage, blockwise causal discovery, and cross-block refinement. The theoretical analysis identifies conditions for recovering the underlying graph and explains sources of false discoveries. Experiments examine computational scaling, graph recovery on synthetic systems, and applications to river discharge and financial time series.

Critical strengths
  1. The implementation addresses substantial computational and memory constraints in large-scale causal discovery. The experiments demonstrate that the proposed workflow can process systems far beyond the sizes considered by the reference implementation.
  2. The paper carefully distinguishes computational feasibility from statistical reliability. The analysis and diagnostic experiments explicitly identify failures caused by screening, missing conditioning variables, and repeated use of the same observations.
Critical weaknesses

-- The recovery guarantees do not directly support the pipeline used for the main scaling results. The recovery analysis requires retesting provisional decisions after assembling the necessary conditioning variables, together with calibration that accounts for selecting and testing candidates on the same observations. The main implementation leaves earlier within-block decisions unchanged and does not apply this calibration. Consequently, the theoretical safeguards are not part of the procedure whose large-scale accuracy and cost are reported. The independent-data confirmation experiment offers a possible remedy, but uses an additional trajectory at smaller scales. Evaluating a corrected procedure under a fixed total observation budget would clarify whether reliable recovery can retain the reported computational benefits.

-- The large-scale accuracy results depend on a particularly favorable signal structure. The main synthetic systems have sparse linear interactions and clearly detectable marginal signals. These conditions support the initial screening, but true parents can be removed when their effects cancel or are obscured by stronger indirect associations. Later refinement cannot recover an edge that never enters the candidate set. The paper demonstrates such failures in small diagnostic examples, which is useful, but these examples do not establish how performance changes as the difficulties become more common in a large system. Broader evaluation of heterogeneous interactions is needed to determine the range in which scaling preserves useful causal accuracy.

-- The reported parameter settings do not fully describe the behavior of the evaluated implementation. The implementation notes disclose that the selected significance level for parent selection was not passed to the batched test, which instead used a fixed default. The stated tuning therefore did not fully control the computation. The proposed method and the reference implementation also allocate their conditioning budgets differently, so matching the overall budget does not make their statistical decisions equivalent. Although the shared-hardware experiments are valuable, these discrepancies complicate the attribution of accuracy and runtime differences. The affected comparisons need to be repeated with corrected settings and justified conditioning choices.

-- The real-data evaluation provides limited independent support for practical causal discovery. The river benchmark reuses the same held-out windows across development iterations in which the scoring or conditioning rules changed, and the selected final configuration was not recorded. The authors appropriately describe the results as descriptive, but the reported advantage therefore remains difficult to reproduce and assess on unseen data. The financial application demonstrates operational feasibility without a reference graph, so it cannot resolve this uncertainty about causal accuracy. A reproducible evaluation on untouched observations would provide stronger support for transferring the synthetic results to real systems.

Questions for authors

Please see weaknesses.

3 comments

Thank you for a careful review. Each of your four points led to a new evaluation with its predictions fixed in advance.

W1. Guarantees vs. the evaluated pipeline; fixed observation budget.

  • What we ran. The confirmation re-test and a selection-aware level, on the same trajectory as the primary runs (T = 4,096; no additional data; Table 2 in §5.3).
  • Result. FDP falls from 1.3–14.5% to 0.17–0.26% from 10⁵ to 2×10⁶ variables. Recall is 0.9998, and the pass adds 1.2–2.8% to discovery time. Independent nulls pass at 0.0091–0.0103 at nominal 0.01.
  • Scope. The level conditions on the screen and is calibrated empirically. The re-test conditions on the target's parents only, at most six of them, and the conditioning sets are chosen from the same data. We do not claim an FDR theorem for the pipeline; Table 1 in §4.3 now states what is established for each procedure.
  • The split-sample version, at the same budget. Discovery on one half of the 4,096 steps and a test of its frozen queries on the other half keeps recall 0.994 at FDP 0.056% at 10⁵ variables, against 0.9998 at 0.17% for the same-data pass. Its discovery took 11.2 h against 26 minutes. Six of nine predictions held; one failed and two missed (App. C.18).

W2. Favourable signal structure.

  • We agree the main systems are a best case for the screen. The revision now says so (§5.1, App. C.2). Each true edge has population lagged correlation about 0.166 against θ = 0.1.
  • The sweep. At 10⁴ and 10⁵ variables, one difficulty at a time plus all together: coefficient spread, cancelling motifs (a direct edge cancelled by an indirect path), persistence, tanh links and heavy-tailed in-degree. Screen recall was predicted from population correlations before any run. The predicted losses are large, and the measured ones match them (10⁵ variables; App. C.11, Table 24):
SettingScreen recall, predictedScreen recall, measuredConfirmed recallConfirmed FDP
Coefficient spread α = 4 / 1 / 0.30.83 / 0.64 / 0.500.83 / 0.64 / 0.500.79 / 0.61 / 0.490.27 / 0.41 / 0.46%
Cancelling share 0.1 / 0.2 / 0.30.97 / 0.93 / 0.900.97 / 0.93 / 0.900.97 / 0.93 / 0.900.22 / 0.27 / 0.30%
Persistence 0.51.0001.0001.0000.64%
tanh share 0.25 / 0.5 / 10.86 / 0.71 / 0.410.85 / 0.71 / 0.410.80 / 0.60 / 0.180.17 / 0.15 / 0.03%
Heavy-tailed in-degree, max 10 / 100 / 1,0000.72 / 0.49 / 0.480.73 / 0.52 / 0.500.66 / 0.50 / 0.490.13 / 0.14 / 0.16%
All combined0.380.390.351.62%
  • The predictions held in 48 of 49 runs; the one miss was 0.011, with more recall than predicted.
  • Cancelling motifs. The screen loses exactly the cancelled direct edges, a third of the edges into the affected targets, and nothing else. As you say, no later stage recovers them.
  • After the screen. Stages 2–3 lose at most 55 true edges per run. The final test drops 3–9% of screened true edges at the spread, in-degree and combined settings, and up to 56% of screened tanh edges.
  • Calibration and precision. At every setting run at 10⁵, independent nulls pass at 0.0052–0.0107 at nominal 0.01. Confirmed FDP is at most 0.64% except with all five difficulties combined: 1.62% at 10⁵, above our 1% bound. We report this as a precision failure and changed nothing.
  • At 10⁶ variables. Twelve of these settings ran at 10⁶ variables (every level of spread, cancelling, tanh and in-degree), with the same predictions. All six held at each (App. C.17, Table 34, Figure 6):
SettingScreen recall at 10⁶Confirmed recall at 10⁶Confirmed FDP at 10⁶
Coefficient spread α = 4 / 1 / 0.30.830 / 0.643 / 0.5020.789 / 0.614 / 0.4870.32 / 0.47 / 0.61%
Cancelling share 0.1 / 0.2 / 0.30.967 / 0.933 / 0.9000.966 / 0.933 / 0.9000.26 / 0.30 / 0.34%
tanh share 0.25 / 0.5 / 10.852 / 0.705 / 0.4130.799 / 0.596 / 0.1810.20 / 0.20 / 0.18%
Heavy-tailed in-degree, max 10 / 100 / 1,0000.725 / 0.517 / 0.5000.662 / 0.497 / 0.4840.19 / 0.22 / 0.24%
  • Screen recall is within 0.008 of the predictions in the table above, and 0.010–0.026 above them at the in-degree settings.
  • The share of edges lost is the same at 10⁶ as at 10⁵ (F1 within 0.004), so the loss follows the kind of edge and not the size of the system.
  • Independent nulls pass at 0.0089–0.0099.
  • Persistence and the combined setting were not run at 10⁶, and the combined setting's failure at 10⁵ stands.
  • What this shows. Your concern is right: a marginal screen loses parents whose marginal signal falls below θ, and later stages cannot recover them. What the sweep adds is that, for a known model, this loss can be predicted before discovery from each edge's population correlation, and that the final test stays calibrated across these settings. It does not show that real systems resemble any of them (§5.4, App. C.11).

W3. PC level and conditioning budgets.

  • The defect. The five batched CI calls in the PC step omitted the level, both within blocks and in the merging PC step, so every VL-PCMCI run removed parents at 0.05. MCI tests and reference PCMCI applied their levels as configured.
  • Unaffected studies. The scaling studies configured 0.05, so they are unaffected.
  • Affected studies. The same-hardware block-merging row and the river benchmark: both configured 0.01 and ran 0.05. The financial panel also configured 0.01 and most likely ran 0.05; we use it for scale only (App. A).
  • In the paper. It now reports the applied level (0.05), with the configured value in parentheses. The defect is fixed.
  • Reruns with the configured level applied:
    • River development windows: mean F1 0.3438 against 0.3456 as run.
    • Untouched river stations: 0.261 against 0.234 (inconclusive under our pre-declared rule).
    • Same-hardware comparison: rerun as a 2×2, PC level as run vs as configured × each method's own conditioning rule vs one shared rule (the reference implementation's default). Five cells, three seeds each, one CPU thread and a 235-minute limit (App. C.7.1, Table 13).
      • Configured level applied: block merging's F1 changes by at most 0.0007 in every cell, and its fit time falls to 0.39–0.96 of the as-run time. The completion frontier stays at 1,000 series (all three fits at 3,000 hit the limit). No conclusion changes.
      • One shared conditioning rule: every gap between block merging and a baseline moves by at most 0.005 F1. Our rule fixed in advance counts a gap within ±0.005 as a tie. At 300 linear series, block merging's deficit to screened PCMCI goes from −0.0062 to −0.0049, from a loss to a tie. We therefore say that part of that gap comes from the conditioning rule, and we report both rows.
      • Runtime: the shared rule makes block merging 2.2–15.5× faster and PCMCI 1.3–2.4× slower. One PCMCI fit at 300 series and all three screened-PCMCI fits at 1,000 hit the limit. Relative to the baselines, block merging's time under the shared rule is 0.04–0.37 of its value under each method's own rule, so the runtime gap widens under the shared rule.
      • Still unequal: the BH families differ, per block for VL-PCMCI and global for the baselines.
  • Reproduction check. Before any change was applied, the reruns reproduced all 60 original fits exactly. The unpatched code at 0.01 returns the same edges as the patched code at 0.05, which confirms 0.05 was in effect.

W4. River evaluation.

  • The selection was recorded. Each method's selected configuration was saved with that evaluation. The submission's "not recorded" was wrong, and App. A and C.4 now list the selections.
  • A one-shot evaluation on untouched observations. No calendar time is untouched, so we used stations no earlier evaluation touched: 9 panels of 9–22 stations, 18 held-out windows, every method frozen, a test confirming no station-time overlap, and decision rules fixed in advance.
  • Results:
    • Against PCMCI: tuned VL-PCMCI 0.234, tuned PCMCI 0.236 (difference −0.001, 95% interval [−0.034, 0.031]). The earlier advantage did not replicate.
    • Against sparse VAR: sparse VAR was more accurate (0.322; −0.088, [−0.130, −0.038]).
    • Against its own default: the tuned configuration fell below VL-PCMCI's default (0.304), which indicates that tuning overfit the reused windows, as you suspected.
    • Cost: VL-PCMCI remained 2.8× faster than PCMCI.
    • With every method at its default (post hoc, not a pre-declared contrast): VL-PCMCI is ahead of PCMCI on the untouched stations (+0.054, [0.022, 0.087]) and level with it on the 30 earlier windows (−0.011, [−0.031, 0.007]); sparse VAR is ahead on both. So neither configuration leads PCMCI on both sets. These data support equal accuracy at lower cost against PCMCI (2.8× to 26× lower fit time), and no accuracy advantage.
  • In the paper. §5.6 and App. C.4 now report this as stated.
  • The final pass on these windows. Applied afterwards to the held-out windows (post hoc, a second use of them), the final pass leaves the default policy's F1 unchanged (0.304 to 0.305) and lowers the tuned policy's by 0.018. No contrast with a baseline changes sign. Two that had included zero now exclude it, both against VL-PCMCI, and one of four predictions failed. The selective level is not valid on these autocorrelated rows, so this describes what the pass does there, not error control. The rules that count all lagged pairs (a third use of the windows) do not change the result either (App. C.15.4).
  • The financial graph. As you say, it has no ground truth. The paper uses it to show operational scale only, and §7 says so.
  • Caveats. The panels are smaller than the original 32–128, and the stations share years and weather with those used before.

Dear Reviewer 6qam,

A brief follow-up, since the discussion period closes soon. Your first two concerns were the gap between the guarantees and the evaluated pipeline (W1) and the favourable signal structure of the main systems (W2). The revision evaluates the complete procedure at the same observation budget (FDP 0.17–0.26%, recall 0.9998 from 10⁵ to 2×10⁶ variables; Table 2, §5.3), and adds a difficulty sweep whose screening losses we predicted before any run and report in full (App. C.11).

If these do not address your concerns, or if anything in our replies is unclear, we would be glad to answer in the remaining hours. If they do, we would be grateful if you could update your review. Thank you for your time.

Reviewer_aFbiOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
3
Presentation
3
Soundness
2
Read review
Paper summary

The paper proposes VL-PCMCI for causal discovery from very high-dimensional time series. It combines global correlation screening, blockwise PCMCI, and cross-block reconciliation to reduce the cost of conditional independence testing. It also analyzes screening failures, missing separating variables, and selection bias from reusing data. Experiments include matched-hardware comparisons, synthetic systems with up to two million variables, targeted stress tests, and two real-world applications.

Critical strengths

1 The paper studies lagged causal discovery on systems with up to two million variables. Although global screening remains quadratic, reducing the expensive testing workload is a meaningful contribution.

2 The paper identifies three consequential requirements: retaining true causes during screening, preserving separating information across blocks, and accounting for data-dependent selection. The counterexamples and stress tests make these requirements concrete. The analysis of false-positive growth also helps explain the large-scale results. These findings provide useful guidance for designing and evaluating other screening and partitioning methods.

Critical weaknesses

1 Corollary 1 and Theorem 2 require a final confirmation step that is not included in the main large-scale experiments. Specifically, cross-block refinement does not revisit previously accepted within-block edges when additional parents become available. The primary runs show increasing false-discovery proportions, reaching 14.51% at two million variables. The stricter-threshold variant in Table 10 is encouraging, reducing FDP to 0.04% with 95.7% recall at one million variables, but it still skips the full confirmation step. The independent-data diagnostic is limited to smaller systems and uses twice the data. Thus, it remains unclear whether the complete procedure, including confirmation and correction for data-dependent selection, preserves the reported accuracy and computational advantages under a fixed data budget.

2 The evidence for reliable performance (beyond the main synthetic setting) is limited: The largest experiments use a narrow family of sparse linear VAR systems, with one primary run at each of the two largest sizes. On CausalRivers, VL-PCMCI achieves approximately the same F1 as sparse VAR but is slower. The paper also lacks empirical comparisons with relevant screening-and-refinement methods such as CEDAR and GRACE, which it already discusses. Comparisons at feasible scales, under shared settings and consistent evaluation criteria, would help establish the method’s accuracy–cost trade-off.

Questions for authors

1 With the total trajectory length held fixed, what precision, recall, runtime, and memory usage does the complete procedure achieve when both final confirmation and an appropriate selection correction are included? I will reconsider my rating for this paper if sufficient evidence (at large scale) is provided.

2 on remark 5. For the lagged process Wt=(Xt,…,Xt−2L)W_t=(X_t,\ldots,X_{t-2L}), its spectral density satisfies fW(ω)=H(ω)fX(ω)H(ω)∗f_W(\omega)=H(\omega)f_X(\omega)H(\omega)^*. Its rank is therefore at most NN, whereas its dimension is (2L+1)N(2L+1)N. For L≥1L\geq1, this gives m(fW)=0m(f_W)=0, making the displayed concentration-rate expression degenerate. Can the authors correct this argument and establish a positive rate under the stated assumptions?

3 How does VL-PCMCI compare with CEDAR or GRACE ? A comparison of recovery quality and runtime at feasible sizes would help clarify the contribution beyond the included PCMCI and sparse VAR baselines.

5 comments

Thank you for the precise questions. Q1 first: at a fixed T = 4,096 with no extra data, the complete procedure has FDP 0.17–0.26%, recall 0.9998 and F1 0.9986–0.9990 from 10⁵ to 2×10⁶ variables. The added pass costs 1.2–2.8% of discovery time.

Q1 / W1. The complete procedure at a fixed trajectory.

We ran it on the same single trajectory as the submission's Table 9 (Table 17 in the revision): screen, Stages 2–3, then a final test of every screened candidate with a selection-aware level. The reported graph keeps the accepted edges that pass it.

  • No extra data. There is no second trajectory and no split.
  • Re-test. Each screened candidate is tested given the target's estimated parents (target side only, at most six).
  • Selective p-value. On the same time points the screen correlation S1 is an affine function of the final test's partial correlation S2 (S1 = A + B·S2). The screen is then a one-dimensional truncation of S2, and conditioning on it gives a same-data p-value (in the style of Lee et al., 2016). Serial dependence changes the slope to B(1+κ)/2, with κ the Bartlett factor. Without this, nulls pass at 1.4–1.6% at nominal 1%.
  • BH family. One BH at 0.01 runs over every screened candidate, not only accepted edges, so the family does not depend on the Stage 2–3 tests. This does not cover conditioning sets chosen on the same data.
NFDP (1 − precision), pipeline → confirmedRecallF1Final-pass timeFinal-pass peak GPU / host
10⁵1.30% → 0.17%0.999790.999018 s3.8 GiB / 2.9 GB
2.5×10⁵2.49% → 0.17%0.999780.999076 s— / 5.8 GB
5×10⁵4.43% → 0.19%0.999800.99893.2 min9.9 GiB / 10.2 GB
10⁶8.05% → 0.22%0.999780.998812.0 min17.6 GiB / 19.3 GB
2×10⁶14.51% → 0.26%0.999770.998646 min32.8 GiB / 37.7 GB
  • Calibration. On candidates with no common ancestor within two steps, the pass rate at 0.01 is 0.0091–0.0103. At 2×10⁶ there are 986,647 such candidates, with Wilson interval [0.0093, 0.0097].
  • Where true edges are lost. At 10⁶, the screen misses 148 true edges, Stages 2–3 lose none, and the final pass removes 504.
  • The remaining false edges (described after the results; App. C.10). Each is either an independent chance edge or the right cause and effect with the delay off by one or two steps. Counting an ordered pair as found when any of its lags is, FDP is 0.05% at 10⁶ and 0.10% at 2×10⁶.
  • Time and memory of a whole run. As one uninterrupted job on one GPU with four CPU cores, discovery takes 7.7–7.8 h at 10⁶ variables and 29.8 h at 2×10⁶, within host allocations of 150 GB and 260 GB (upper bounds, not measured peaks). With the final pass the complete procedure takes 7.9–8.0 h and 30.6 h, so the pass adds 2.6–2.7% (App. C.9, C.10).
  • Replicates. Four more graphs at 10⁶, two of them run afresh, give FDP 0.21–0.22% and recall 0.99976–0.99979. A fresh run at 2×10⁶ gives 0.26% (App. C.10, Table 19).

Comparison with the strict level you mention.

  • Bonferroni at 0.01/(N²L) on the same final statistic has zero false edges, with recall 0.986 at 10⁶ and 0.978 at 2×10⁶. The selective level keeps recall at 0.9998, so its gain over Bonferroni is recall. (Applied inside Stage 3, as in the submission's Table 10, now Table 18, the strict level gave recall 0.957 at 10⁶.)
  • BH over all N²L pairs at 0.01/c(M) (Benjamini–Yekutieli), computed post hoc, beats our selective level at 4,096 steps: FDP 0.025–0.033% against 0.17–0.26%, at recall 0.99982–0.99995. The selective level keeps more recall only on shorter series (0.955 against 0.904 at 2,048 steps). It remains the reported rule because it was declared first; §5.3 says so.

Scope.

  • The selective p-value is exact only for Gaussian residuals with a fixed conditioning set. Ours is estimated, so we report measured FDP and claim no FDR theorem for the pipeline. App. B.7 states the bound that BH over all N²L pairs has when each single test is valid, and why the pipeline does not meet that condition.
  • With Laplace innovations at 10⁶, FDP is 0.23% and nulls pass at 0.0099 (App. C.15.2). With series shortened to 1,024 steps the procedure fails: recall 0.29 and FDP 2.31% (App. C.15.3).
  • A split-sample version is now measured at the same 4,096 steps (App. C.18): recall 0.994 at FDP 0.056% at 10⁵ variables, with discovery taking 11.2 h against 26 minutes.

Q2. Remark 5.

  • You are right. f_W(ω) = a(ω)a(ω)ᴴ ⊗ f_X(ω) has rank at most N, so the displayed rate was degenerate. The error was using f_W for covariance eigenvalues.
  • The repair. Cov(W_t) is the block-Toeplitz covariance of 2L+1 consecutive observations of X, so its eigenvalues lie in [2π𝔪(f_X), 2π𝔐(f_X)], and by interlacing so do those of every query block. 𝔪(f_X) > 0 for a stable VAR with positive innovation variances.
  • The two-coordinate bound. A two-coordinate sub-process gives ℳ(f_W, 2) ≤ 2ℳ(f_X, 2).
  • The resulting rate. Lemma 3 then gives b·T_eff ≍ n(s+2)⁻²(𝔪(f_X)²/(𝔐(f_X)ℳ(f_X, 2)))², which is positive under the stated assumptions.
  • In the paper. App. B.4 now has the full proof, including the centering term. Theorem 2 is unchanged as a statement, since it is conditional on Assumption 2; only this sufficient route was wrong.

Q3 / W2. CEDAR and GRACE.

  • Setup. We run both through their authors' package (causalts) on the same generator, scorer and single-thread hardware rule as the paper's same-hardware comparison, at N = 100 and 300, and on 32–128-variable panels. We also run them in their own setting (T = 1,000, L = 5), including GRACE's benchmark generator.
  • Tuning. Each gets its paper defaults plus exactly the tuning budget our baselines received.
  • Results on the same-hardware cells (mean F1 / median fit time, one CPU thread, 235-minute limit, three seeds; App. C.8, Table 14):
MethodLinear 100Linear 300Linear 1,000tanh 100tanh 300
VL-PCMCI (frozen)0.9983 / 2.7 s0.9985 / 6.8 s0.9981 / 25 s0.460 / 1.8 s0.476 / 3.5 s
CEDAR, tuned0.9961 / 9.4 min0.9885 / 90 mintimeout0.969 / 9.0 min0.956 / 75 min
CEDAR, default0.6528 / 9.7 min0.4041 / 86 mintimeout0.566 / 9.7 min0.329 / 88 min
GRACE, tuned0.8600 / 52 mintimeoutnot launched0.002 / 51 mintimeout
GRACE, default0.8513 / 95 mintimeoutnot launched0.002 / 187 mintimeout
PCMCI0.9961 / 12 min0.9972 / 92 mintimeout0.950 / 9.7 min0.924 / 96 min
Sparse VAR0.9978 / 4.0 s0.9943 / 33 s0.9833 / 9.2 min0.969 / 8.1 s0.966 / 37 s
  • Accuracy–cost. On linear systems VL-PCMCI is ahead of the stronger rival, tuned CEDAR, by 0.002 and 0.010 F1 and is 205× and 797× faster on the same CPU. These times are without the final pass, which adds 18–20 s (App. C.15.1). GRACE finishes 100 variables and CEDAR 300; neither finishes 1,000, where VL-PCMCI takes 25 s. The reruns of PCMCI, sparse VAR and VL-PCMCI reproduce the submission's numbers to four digits.
  • The 90 tuning panels (32–128 variables). Tuned CEDAR ties our tuned baselines (F1 0.9885 against 0.985–0.987).
  • Their regime (T = 1,000, L = 5). On our linear generator VL-PCMCI has the highest F1 (0.85–0.95), but its FDP rises to 25% at 100 variables. On GRACE's benchmark generator GRACE leads clearly (0.81–0.83 against 0.42–0.53), and five of our 30 fits there failed with an error, which we report as failures.
  • Nonlinear systems. Tuned CEDAR, PCMCI and sparse VAR beat VL-PCMCI's frozen configuration on tanh systems. This is the linear-screen limitation; the revision states it in §5.2 and §7.
    • We also ran the final pass on the tuned variant, at that variant's threshold (pre-declared). F1 is 0.892 and 0.916 at 100 and 300 variables, against 0.910 and 0.927 before the pass, and still behind sparse VAR, tuned CEDAR and PCMCI (0.92–0.97). The limitation stands.
  • Published defaults, as measured. CEDAR's published configuration keeps recall but has precision 0.49 and 0.25 on the linear cells. On tanh systems, GRACE's gates rank the true edges almost perfectly (AUROC ≥ 0.998) but stay below its 0.5 threshold, so it outputs almost no cross edges. Three of our pre-declared predictions about these methods were wrong, and App. C.8 lists them.

W2. Breadth of evidence.

  • Heterogeneity. The sweep is in our reply to 6qam, with tables. Twelve settings ran at 10⁶ variables: confirmed FDP 0.18–0.61%, confirmed recall from 0.97 down to 0.18, following the predicted screen recall, and F1 within 0.004 of the 10⁵ value (App. C.17). With all five difficulties combined at 10⁵, FDP is 1.62%, above our 1% bound.
  • Rivers. On untouched stations VL-PCMCI ties PCMCI (F1 0.234 against 0.236) and trails sparse VAR (0.322), at 2.8× lower cost than PCMCI. We revised §5.6 accordingly.
  • Noise and length. Laplace innovations leave the 10⁶ result unchanged (F1 0.9987 against 0.9988). The method needs long series: 3,072 steps suffice at 10⁴ and 10⁵ variables, but recall is 0.909 at 2,048 steps (10⁵ variables) and 0.29 at 1,024 (10⁴), with FDP above our 1% bound at both (App. C.15.2–C.15.3).

Dear Reviewer aFbi,

A brief follow-up, since the discussion period closes soon. Your main question (Q1/W1) was whether the complete procedure, with confirmation and a selection correction, works at a fixed trajectory length. We ran it: at T = 4,096 with no extra data, FDP is 0.17–0.26% and recall 0.9998 from 10⁵ to 2×10⁶ variables, and the added pass costs 1.2–2.8% of discovery time (Table 2, §5.3).

If this does not address your concern, or if anything in our replies is unclear, we would be glad to answer in the remaining hours. If it does, we would be grateful if you could update your review. Thank you for your time.

Reviewer_z2LSOpenReview ↗
Rating
3(+1)
Confidence
3(−1)
Informativeness
2
Presentation
1
Soundness
1
Read review
Paper summary

The paper proposes a three-stage algorithm based on PCMCI for high-dimensional causal discovery. The algorithm first applies a cheap screening operation to all candidate pairs to build a sparse candidate graph. Different partitioning rules are then applied depending on the number of variables to divide the variable time series into blocks. PCMCI is applied within each block to obtain within-block parent estimates. These estimates then serve as conditioning sets for MCI tests on cross-block candidates that survived the initial screening. The paper proposes two procedures for identifying cross-block causal relationships: REFINE and MERGE. REFINE keeps within-block decisions fixed and only adds cross-block edges through two-pass MCI testing. MERGE determines neighboring blocks using a coarse graph built from block-averaged time series. It then reruns full PCMCI on the combined individual variable time series from neighboring blocks to revise within-block parent estimates.

Critical strengths
  1. The paper is well-motivated and the simulations demonstrate impressive scalability on causal discovery for high-dimensional data.
  2. The overall three-stage algorithm is well-structured, and the REFINE operation is well-aligned with why MCI tests are needed for time series causal discovery. The MERGE operation provides a practical alternative to adjust the within-block parent estimates.
  3. The paper includes both simulation studies and real-data applications.
Critical weaknesses
  1. The presentation of the paper is limited, and the balance between the main paper and the appendix should be further improved. Important details, such as how to partition variables into blocks and how to decide which blocks to merge, are unclear in the main text. Figures 2 and 5 are also unclear in terms of what the different edge types mean and how to read them.
  2. The theoretical novelty is limited. Theorem 1 is a natural extension of existing PCMCI theory. The more substantive gap is that the MERGE procedure has no formal correctness guarantee: Corollary 1 covers only REFINE, and the validity of using block-averaged time series to determine neighboring blocks is not addressed theoretically, which is a nontrivial assumption.
  3. The key details of the data-generating process seem to be missing, making it hard to assess whether the reported accuracy is significant.

Although the method is an incremental extension of PCMCI without novel theoretical contributions and relies on marginal screening recall, its high-dimensional simulation results are impressive. However, its data-generating process, particularly how ground-truth parents are selected, is insufficiently described, making it difficult to assess whether the simulations favor the screening and block-wise method. Moreover, the algorithm does not account for potential false positives arising from parents in other blocks. I therefore recommend rejection but am open to increasing my score if all concerns are adequately addressed.

Questions for authors
  1. What distributional assumptions are needed for the theoretical guarantee? Does it assume Gaussian noise?
  2. There are no comparable baselines for the high-dimensional data in Figure 4. How about applying PCMCI directly to the block-wise datasets, without the REFINE or MERGE procedure, as a baseline to show the improvement from these procedures?
  3. On the CausalRivers dataset, the F1 score for PCMCI is 0.243, while the cited paper reports a relatively higher AUROC. What differs in scale between the setting reported in the cited paper and the one in the main paper?
  4. It is suggested to include error bars in Figures 3 and 4.
  5. Regarding the data-generating process, how are parents and their lags selected? How are the graphs ensured to pass the screening threshold, and how is stationarity ensured?
  6. Within-block false positives caused by parents in other blocks may persist. The authors suggest that a final confirmation re-test could address this issue, but it was not performed in the experiments. Could the authors clarify why this step was omitted and whether its omission affects the reported results?
4 comments

Thank you for the detailed review and for being open to raising the score. This comment answers Q6, Q5/W3, Q1 and Q2. Our second comment answers W1, W2, Q3, Q4 and your summary paragraph.

Q6. Why the confirmation re-test was omitted, and whether it matters.

  • It was not implemented at submission. It is now part of the evaluated procedure (§3 "Final pass"), and Algorithm 1 returns its result.
  • Effect. It matters for precision at scale. On the same trajectory it re-tests every screened candidate, and so every accepted edge, including within-block edges whose parent sits in another block, and it corrects for the selection behind the N² growth of false edges. FDP falls from 1.3–14.5% to 0.17–0.26% from 10⁵ to 2×10⁶ variables, with recall 0.9998 (Table 2, §5.3; details in our reply to aFbi).
  • Reported results. The submission's numbers, without the final pass, stay in the paper. Table 2 puts the complete procedure beside them.

Q5 / W3. Data-generating process.

  • Now described in full (§5.1, App. C.2):
    • Each series has three distinct non-self parents, each outside its community with probability 0.5.
    • Lags are uniform on {1,…,L}, and coefficients are ±0.15 with a random sign.
    • Each series has an own lag-1 coefficient of 0.3.
    • The absolute incoming coefficient sum is 0.75 < 1, a contraction, which gives stationarity.
    • Series start at zero with a 256-step burn-in, and innovations are Gaussian.
    • Blocks are random and independent of the communities.
  • Passing the screen. Nothing enforces it, but each true edge has population lagged correlation about 0.166 against θ = 0.1, so true parents clear the screen by design. We state that the scaling study is therefore a best case for the screen, and we added a heterogeneity sweep that measures what happens otherwise (see our reply to 6qam).

Q1. Distributional assumptions.

  • No Gaussian assumption for the oracle results. Theorem 1 and Corollaries 1–2 need Assumption 1 and a perfect CI test.
  • For partial-correlation tests, a stable linear VAR with independent innovations suffices. Lemma 1 gives zero partial correlation under d-separation without Gaussianity. The oracle results then also need faithfulness for partial correlations (stated in App. B).
  • Where Gaussianity enters. In two places, and §4 now names both. The theory uses it only through Remark 5, the sufficient route to Assumption 2. The selective p-value of the final pass is exact only for Gaussian residuals (App. A.1), so we check its calibration empirically.
  • Tested at scale. We reran the complete procedure with Laplace innovations (unit variance, excess kurtosis 3) and nothing else changed (App. C.15.2).
    • At 10⁶ variables, F1 is 0.9987 and FDP 0.23%, against 0.9988 and 0.22% on the same graph with Gaussian noise.
    • The selective test stays calibrated there: 258,105 independent nulls pass at 0.0099 at nominal 0.01.
    • On one of two graphs at 10⁵, nulls passed at 0.0156, above our 0.013 bound, and recall missed its predicted bound by eight edges. We report both as failures. That graph's confirmed FDP was still 0.17%.

Q2. Block-only baseline.

  • Recall ceiling. Without reconciliation, recall is at most the within-block share of true edges, about 1/K for K random blocks: 5.0%, 2.0%, 1.0% and 0.5% at 10⁵, 2.5×10⁵, 5×10⁵ and 10⁶ (for example, 15,207 of 3,000,000 at 10⁶).

  • With reconciliation, recall is 0.99995.

  • Measured on the five scaling systems (App. C.9). PCMCI within the learned blocks, with no cross-block step:

    N10⁵2.5×10⁵5×10⁵10⁶2×10⁶
    Block-only recall0.0500.0200.0100.00510.0025
    Block-only F10.0950.0400.0200.0100.005
    Block-only false edges1323336141,2002,450
    VL-PCMCI F10.9930.9870.9770.9580.922
    VL-PCMCI F1, with the final pass0.9990.9990.9990.9990.999
  • Reconciliation is what makes the method work. Blocks alone find nearly every within-block edge, but those are 0.25–5% of the true edges.

  • Screen-only baseline (App. C.9). Accepting every screened pair, with no conditional test, keeps the recall (0.99995) but has FDP 31.5%, 32.1%, 33.0%, 34.9% and 38.2% at the five sizes, so its F1 is 0.813, 0.809, 0.802, 0.789 and 0.764. The screen supplies the recall. The conditional tests cut FDP to 1.3–14.5%, and the final pass to 0.17–0.26%. §5.3 now sets the four stages side by side at 10⁶ variables.

W1. Presentation.

  • Partition and merging rules are now in §3: partition by size regime, the coarse graph from block means, its level, and the merge rule.
  • The complete algorithm. Algorithm 1 now ends with the final pass and returns the confirmed graph. Table 1 in §4.3 states what is established for each procedure: the refinement, block merging, the final pass, and the two alternatives we measured.
  • Figures 2 and 5 have legends for every edge type; Figures 1–5 have larger labels (7–8 pt).
  • We used the tenth page for the complete-procedure table and the generator description.

W2. Theory.

  • Novelty. We agree Theorem 1 is a natural extension of PCMCI theory. The contribution we claim is:
    • the three requirements and the failure modes that show each is necessary;
    • the false-edge law that predicts the N² growth;
    • now, a same-data selective final test that cuts FDP to 0.17–0.26% at 10⁵ to 2×10⁶ variables, shown empirically and without an FDR theorem.
  • MERGE. You are right: routing by block means has no guarantee. Figure 2(d) shows it failing, and it failed in 3 of 15 of our fits. Corollary 2(c) and Theorem 2 cover block merging only under a routing condition. A new remark gives a rule that meets it: with the screened coarse graph and no neighbour cap, routing follows from screening recall. It is affordable only on small panels.
  • Which results rest on which rule. Every scaling result (Figure 4 and Table 2, 10⁵ to 2×10⁶ variables) uses the cross-block refinement, which Corollary 1 covers under its oracle assumptions, with no routing condition. Block merging appears only in the same-hardware comparison and the river study.
  • Routing by block means, measured (App. C.16, Table 33). You called it a nontrivial assumption, and our runs bear that out.
    • The measurement (made after the fact, from the stored merge logs). In the three failing fits the block means joined 6, 2 and 8 of the 12 block pairs. The fits missed 774, 100 and 188 true edges, and 774, 92 and 157 of these were never tested. The first is the outlier seed of Figure 3.
    • The rule with the guarantee (protocol fixed before any new fit). We reran all 15 datasets with every pair of blocks merged. Every true cross-block edge was then tested. Mean F1 rose from 0.930 to 0.975 at 1,000 linear series, and from 0.910 and 0.927 to 0.967 and 0.958 on tanh systems (sparse VAR: 0.969 and 0.966). Seven of eight predictions held; the cost prediction failed in part.
    • Limits. These are four-block systems of at most 1,000 series, where merging every pair costs as much as the whole system. Routing on the river panels was not measured. The submission's rows are unchanged, and the new ones are beside them.

Q3. CausalRivers F1 vs the cited AUROC.

  • Different metrics on different problems. CausalRivers reports threshold-free AUROC at the best hyperparameters on 3–10-node subgraphs (PCMCI 0.62–0.83). We report F1 at a fixed operating point on 32–128-station panels, where edge density falls roughly as 1/N. Their own best-threshold F1 for PCMCI is already 0.47 at 10 nodes.
  • On our windows, PCMCI's AUROC is 0.800 tuned and 0.827 with defaults, inside their range (App. C.4).
  • On untouched stations (a new one-shot evaluation; see our reply to 6qam), PCMCI's AUROC is 0.681 tuned and 0.708 with defaults.
  • Our river claim changed. On those untouched stations VL-PCMCI ties PCMCI and trails sparse VAR.

Q4. Error bars.

  • Figure 3: added. Bars show the range over the three seeds of every cell, for both time and F1. The seeds agree closely, with one exception: block merging at 1,000 series, where one seed missed 774 of 3,000 true edges (F1 0.837) and the other two found them all. App. C.7 states this. We now know the cause: the block means did not join the blocks of those 774 edges, so they were never tested (App. C.16; see W2 above).
  • Figure 4: we now have six graphs at 5×10⁵, five at 10⁶ and two at 2×10⁶, each with its own data and its own pipeline run. Seven of the replicates use blocks of 1,000 variables in place of the primary runs' 5,000. The graphs differ by at most 0.0002 in F1 and, where recorded, 0.5% in false edges. That is smaller than the markers, so the caption of Figure 4 and App. C.9 state the ranges instead of drawing bars. The complete procedure agrees as closely: confirmed FDP 0.21–0.22% across the five graphs at 10⁶, and 0.26% for both graphs at 2×10⁶.

Summary paragraph: false positives from parents in other blocks. These are what the final re-test targets. In the rebuilt study of observing more variables (App. C.14), with every driver observed, false edges between children of one driver fell from 225 to 4 over five seeds, and the re-test's conditioning set held the driver at its true lag every time. Nearly all of the 225 were same-block pairs whose driver sits in another block. While the driver is hidden, 86–96% of such edges stay.

Dear Reviewer z2LS,

A brief follow-up, since the discussion period closes soon. You indicated that you were open to revisiting your score. In short: the confirmation re-test (Q6) is now implemented and evaluated as the final pass (§3.4; Table 2, §5.3), and the data-generating process (Q5/W3) is described in full (§5.1, App. C.2). Our two comments answer the remaining questions point by point.

If anything is still open or unclear, we would be glad to answer in the remaining hours. Otherwise we would be grateful if you could update your review. Thank you for your time.

Thank you for the detailed responses and additional experiments! Since my main concerns about the data-generating process and Q6 have been addressed, I have raised my score. However, the lack of theoretical guarantees for the final pass and for block merging, and the fact that the headline results are obtained in a best-case setting for the screening step, remain limitations that should be taken into account. Since the final pass was added during the discussion period and I could not fully verify it, I have also lowered my confidence.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

Related papers

Loading the map…

Discussion (0)

Sign in to comment.